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Under review as a conference paper at ICLR 2027

RethinkDrive: Supervision Targets for Lightweight Trajectory Refinement in End-to-End Driving

Abstract

Candidate-based driving planners must select one trajectory from many plausible alternatives. A candidate's driving score can guide this choice, but does not establish its value as a training target. We present RethinkDrive, a lightweight refinement procedure and controlled study of this distinction. With the planner and candidate pool frozen, we compare metric-derived targets with targets anchored to recorded human trajectories, which are used only in training. We evaluate learned rankings before and after combining their scores with the planner's. On NAVSIM, reference supervision improves a diffusion planner, mainly by making successive plans more temporally consistent, with some loss of progress and drivable-area compliance. The gain persists with disjoint training and validation logs and without score fusion; two validation-selected rules do not reproduce it. Fusion even reverses the comparison between a hard reference target and a validation-selected soft target on this planner. On a vocabulary-based planner, it reduces large differences between learned rankings to similar final scores, without a resolved improvement over the baseline. These findings show that supervision quality must be assessed through both the learned ranking and its use in the deployed selection rule.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Autonomous driving, End-to-end planning, Trajectory selection, Trajectory refinement, Imitation learning, Supervision design, Metric saturation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

This paper investigates supervision targets for trajectory selection when both the planner and the candidate pool are frozen. RethinkDrive trains a lightweight, attention-based selector using the candidate closest to the recorded human trajectory as its supervision target and, at inference, combines the learned scores with the planner’s scores. Controlled comparisons examine metric-derived targets, tie handling, and hard versus soft reference supervision. Experiments on DDv2 and DriveSuprim separately analyze target scores, learned rankings, and final fused performance.

Critical strengths
  1. The controlled experiments substantially strengthen the credibility of the local findings. The main target comparisons hold the planner, candidate pool, selector architecture, and training recipe constant. Several plausible alternative explanations are addressed through log-disjoint retraining, matched-context controls, removal of score fusion and the auxiliary safety penalty, and validation-selected rule baselines. In particular, reference supervision still improves DDv2 without fusion, so its benefit cannot be attributed entirely to combining scores. The explicit reporting of negative results and behavioral costs further strengthens the study.

  2. Separating learned rankings from fused execution offers a useful evaluation lesson. On DDv2, soft reference supervision performs better than hard reference supervision before fusion, but their ordering reverses after fusion. On DriveSuprim, fusion substantially compresses differences between learned selectors without establishing an improvement over the native planner. These comparisons illustrate how final aggregate performance alone can obscure meaningful differences between supervision targets.

Critical weaknesses
  1. The demonstrated practical benefit remains tied to a local baseline whose unusually low temporal comfort is unexplained. In the primary DDv2 configuration, the approximately +3.93 pp EPDMS improvement decomposes into an EC contribution of +4.36 pp and a remaining contribution of −0.42 pp (Table 21). Reported progress falls from 91.2 to 87.8, and drivable-area compliance from 97.8 to 96.7. Although the comfort improvement is valuable, its significance depends on the representativeness of the starting point: local native EC is 34.0, and Appendix F does not resolve this discrepancy. On DriveSuprim, the improvement is only +0.29 pp, with a confidence interval spanning zero, and the refined score is numerically almost identical to that of coarse-only selection. Although validation-selected fusion improves the DDv2 trade-off, the evidence still leaves substantial uncertainty about the benefit on a planner that already performs well.

  2. The explanatory contribution remains limited relative to the modest methodological novelty. Reference-based trajectory supervision and learned scoring are established ingredients; Hydra-MDP, for example, already combines distance-based imitation targets with metric supervision. The main contribution therefore rests on the controlled study. However, that study does not yet establish when a particular target should be preferred: tie handling and partial metric alignment leave much of the metric-target deficit unexplained, while the hard–soft comparison depends strongly on execution. These limitations do not invalidate the observed comparisons, but they leave the paper with a useful descriptive finding rather than sufficiently developed, transferable guidance for supervision design.

Questions for authors
  1. What explains the discrepancy between the local DDv2 native EC of 34.0 and the published value discussed in Appendix F? Can the checkpoint provenance and evaluation differences be identified? Evidence that the refinement retains a meaningful benefit under a matched released-checkpoint configuration would materially strengthen my assessment of its practical significance.

  2. Appendix O.4 notes that a common logit shift preserves the training loss but can change fused selection. Does the hard–soft reversal persist after controlling for this freedom? For example, through centered logits and validation-selected calibration or fusion weights for each target, using the reported evaluation criterion? This would help determine whether the result yields a robust supervision-design insight or primarily reflects the particular score parameterization.

1 comment
AuthorsOpenReview ↗

Benefit remains on the matched released checkpoint, and the fusion rule, not the target, set the hard–soft order

Thank you sincerely for your careful and precise review, and we are truly sorry for our late answer. The reruns and the calibration control you proposed took several days, and we wanted each answer to come with its result and our reading.

In the revised PDF your changes are orange, and margin tag 3-n points to answer [3-n].

[3-1] Weakness 1

The demonstrated practical benefit remains tied to a local baseline whose unusually low temporal comfort is unexplained.

We agree with your reading, and we would like to add why the gain takes this form. The low extended comfort (EC) is documented in part and not reproduced (answer [3-3]). It comes from the publicly released weights, which we had to use as they are. Your decomposition holds, and the interval of the −0.42 is [−0.89, +0.04] (Table 21). Since EC is the only official term comparing successive plans and the training score has none, a target from one continuous human drive adds most where the planner's consistency is weakest. The lower progress is already present in the target (87.68 against 87.77). Of the drivable-area drop of −1.12 [−1.56, −0.69], 41% comes from the 5.0% of scenes where the target itself does not comply (Appendix Y).

On representativeness, the gain shrinks as native EC rises (34.0 / 41.7 / 55.5 / 77.3 gives +3.93 / +3.21 / +2.37 / +0.29, Table 36). On a further planner that already performs well, GTRS-Aug (native EC 78.2), the gain predicted in advance was +0.29, and we observed −0.37 [−0.78, +0.07], within its tolerance (Appendix X). At 91.0 the fitted line gives −0.76, and we claim no gain there. On DriveSuprim we claim no benefit (+0.29 [−0.18, +0.81]), and the refined score equals coarse-only selection. So where the benchmark leaves room, the gain is consistent and can be predicted.

Where to check. Section 5.6 (p. 9, lines 479–485) and limitations (p. 10, line 518).

[3-2] Weakness 2

The explanatory contribution remains limited relative to the modest methodological novelty.

Thank you, we agree that the ingredients are established, and our contribution is the controlled study. Hydra-MDP trains distance and metric heads jointly, whereas we ask which single target to train on with all else frozen. The study suggests three rules that we hope will carry over.

  1. Prefer the demonstration target where the per-frame score is tied or blind to successive plans. The tie-break recovers 4.61 [4.12, 5.13] of the 13.13 points between the two selectors, and 8.52 remain unexplained. Even a metric target with the benchmark's between-frame term trains selectors about 6 points below the reference target (Appendix AA). On the third planner the reference target is ahead too (+1.95 [+1.08, +2.84] alone).
  2. Compare targets alone and under a calibrated fusion. The hard–soft order was set by the fusion rule (answer [3-4]).
  3. Expect a gain in proportion to EC headroom.

We agree that these are only first rules, from one benchmark and in open loop.

Where to check. Section 5.3 (p. 8, lines 392–394), Section 5.6 (p. 10, lines 511–517).

[3-3] Question 1

What explains the discrepancy between the local DDv2 native EC of 34.0 and the published value discussed in Appendix F? We could document it only in part and not reproduce it, but on the released checkpoint the benefit remains. On provenance, our file is byte-identical to the released selector checkpoint (Appendix P). The maintainers state publicly that the NAVSIM v1 and v2 weights differ and that the published row uses the scorer before a bug fix. We could not obtain those weights. On evaluation, sampling moves EC from 34.0 to 55.5, never near 91.0. In the matched released-checkpoint setting you suggest, with 20 trajectories, the count that the DDv2 paper states for its diversity analysis, the gain is +3.21 [2.80, 3.62], and +2.37 [1.99, 2.74] with zero initial noise (Table 33). A benefit thus remains on the released checkpoint, and we claim none for the published system.

Where to check. Section 5.6 (p. 9, lines 479–485), Appendices P, B and F.

[3-4] Question 2

Does the hard–soft reversal persist after controlling for this freedom? Thank you for this precise question. Under your control the reversal does not persist, which shows where it came from. We ran the control you describe (Appendix S, fixed before any run), with centered logits and a fusion weight selected per target on validation by the official EPDMS. The hard target led by +4.66 at the fixed weight and by +0.17 [−0.02, +0.36] after this calibration. So the earlier ordering reflected the score parameterization, not the targets. We think this sharpens the lesson you highlighted: how the deployed rule is calibrated can decide which target looks better, so targets should be compared alone and under a calibrated fusion.

Where to check. Section 5.5 (p. 8, lines 428–431) and Table 4 (p. 10, lines 500–502).

If any question remains, we will answer it right away.

Reviewer_3NgDOpenReview ↗
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Informativeness
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Paper summary

This paper presents RethinkDrive, a selection-based approach for refining the output of a frozen driving planner. The paper first observes that supervision from rule-based metrics can be ambiguous since many candidate trajectories attain the same maximum driving score. It then trains a lightweight selector using the candidate closest to the human trajectory as a learning target. At inference, the selector score is fused with the score of the frozen planner for final selection. The method is benchmarked on NAVSIM navtest and navhard. Integrated with DiffusionDriveV2, RethinkDrive improves EPDMS by 3.9 on navtest and 1.6 on navhard.

Critical strengths
  1. The empirical performance on NAVSIM is strong. RethinkDrive consistently improves the DiffusionDriveV2 baseline on both navtest and navhard, while adding only 0.52M parameters and approximately a latency of 0.56 ms.

  2. The experimental analysis is detailed. The authors report not only the final EPDMS but also the relevant trade-offs. In particular, the improvement mainly comes from substantially better temporal comfort, whereas ego progress and drivable-area compliance may decrease. The paper also clearly reports inconclusive results on DriveSuprim and exploratory closed-loop experiments.

Critical weaknesses
  1. The motivation and presentation are difficult to follow in several places. In Figures 1(b) and 2(b), the candidate closest to the human trajectory is used as the one-hot training target even though its cached driving score can be zero. This appears counterintuitive. The observation that metric maxima contain many ties does not by itself justify the nearest-demonstration candidate as the preferred target. The authors should clarify the motivation of this design.

  2. The major evaluation of the paper is restricted to NAVSIM. NAVSIM uses non-reactive trajectory evaluation, in which the selected actions do not affect future observations. The appendix contains exploratory Bench2Drive results, but the results seem to be incomplete and fail to cover all 220 routes. An evaluation on a benchmark such as HUGSIM [1] (which is often used for zero-shot evaluation of NAVSIM-trained planners, such as DrivoR [2]), or a complete CARLA/Bench2Drive experiment, would strengthen the paper.

  3. There are also some issues with the presentation. Some sentences read like a response to anticipated objections rather than an argument. For example, Line 132 says "Soft reference is a distance-target control, not a Hydra-MDP reproduction." Moreover, Figure 2 lacks details of the proposed method. A clearer figure showing the detailed architecture and inputs of the selector network would improve readability.

[1] Zhou H, Lin L, Wang J, et al. Hugsim: A real-time, photo-realistic and closed-loop simulator for autonomous driving[J]. IEEE Transactions on Pattern Analysis and Machine Intelligence, 2025. [2] Kirby E, Boulch A, Xu Y, et al. Driving on registers[C]//Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2026: 32058-32069.

Questions for authors

I don't have other questions. Please refer to the Critical Weaknesses section.

1 comment
AuthorsOpenReview ↗

Demonstration target supported by a new control, and complete Bench2Drive and HUGSIM closed-loop tests added

We are truly grateful for your thoughtful review, and we sincerely apologize for the late reply. Running the closed-loop evaluations you asked for, on Bench2Drive and HUGSIM, took several days, and we wanted to reply with finished results and analysis. In the revised PDF your changes are green, and margin tag 2-n points to answer [2-n].

[2-1] Weakness 1

The observation that metric maxima contain many ties does not by itself justify the nearest-demonstration candidate as the preferred target.

We agree with you. Ties alone do not justify it, and a new paragraph of Section 3 now states the motivation. The one-hot label is a training target, not a claim that this candidate has the best score. The cached score leaves the target open (its maximum is shared in 85.3% of the training scenes) and has no term that compares successive plans. The recorded trajectory names one candidate and belongs to one continuous drive. Executed directly, the nearest candidate passes the extended-comfort (EC) test on 62.4% of scenes and the metric maximum on 18.9% (Appendix U).

The zero score in Figures 1(b) and 2(b). We understand that this looks counterintuitive, so we measured it. The target's cached score is 0 in 2.69% of the training scenes, at a median of 0.13 m from the recording. Retraining without these targets changes nothing (−0.03 [−0.09, +0.02], Appendix T). The selector does not reduce the share of zero-score plans, and the Ethics Statement says so.

Evidence and its limit. The reference target is ahead of the metric maximum on DDv2 (87.65 against 74.52 fused) and on a third planner (+1.95 [+1.08, +2.84] alone, through EC only). We also ran the control that this argument calls for. We trained selectors on a metric target with the benchmark's own between-frame term (EC), fixed beforehand, with two tie rules. They reach 81.45 and 81.22. The term helps the metric target (74.52 without it), but both selectors stay below the reference target (−6.19 and −6.43) and below the native planner (83.71). Its labels even pass the EC test more often (98.3% against 79.3%). So this term does not produce the gain (Appendix AA). So far we have tested one such construction.

Where to check. Section 3 (p. 4, lines 203–208), Figure 1 caption (p. 2, lines 78–81), Section 5.2 (p. 7, lines 366–367), Appendices T, U and AA.

[2-2] Weakness 2

The appendix contains exploratory Bench2Drive results, but the results seem to be incomplete and fail to cover all 220 routes.

You are right, and we ran both evaluations you suggested. Unlike NAVSIM, both are closed loop, with designs fixed beforehand.

Complete Bench2Drive. It covers all 220 routes with three complete runs per configuration and a matched planner-only baseline (Appendix V). The Appendix H selector, a small classifier that edits TCP's single plan without seeing the scene, lowers TCP's driving score by −10.84 [−14.51, −7.28], and a rebuilt version by −13.74 [−17.64, −9.90]. Its edits move the plan sideways, and lane departures rise from 8.6% to 23.8% and 31.3% of route runs (Table V3, post hoc). Our NAVSIM selector instead chooses among the planner's own candidates. The single run of Appendix H is replaced by this experiment.

HUGSIM [1], with the selector of the NAVSIM tables itself. All 436 scenarios, zero-shot as for DrivoR [2], three runs per configuration (Appendix V.1, Table V4). No loss was detected on either planner (−0.45 [−1.75, +0.82] on DriveSuprim, +0.92 [−0.51, +2.36] on DDv2, positive in all three run pairs), and DDv2's plans became far more comfortable (27.9 to 57.9), as on NAVSIM. On DriveSuprim a descriptive score of the driven trajectory is lower (−1.48 [−2.71, −0.27]). HUGSIM limits what can show up here, since its score has no term for consistency between successive plans, where our gain lies, and it renders no LiDAR for DDv2. So no closed-loop gain is established, but no loss was detected and the mechanism carried over.

Where to check. Abstract (p. 1, lines 28–30), limitations (p. 10, lines 518–524), Appendix V.

[2-3] Weakness 3

Some sentences read like a response to anticipated objections rather than an argument.

Thank you, we rewrote them and redrew the figure. Sixteen sentences or clauses in Sections 1 to 6 and one in the Ethics Statement are now plain statements. Your example of Line 132 now begins "The soft-reference control replaces the one-hot target" (p. 3, lines 146–147). The new Figure 2 (p. 4, caption lines 189–195) shows the missing details, namely the inputs (16 geometry features and six predicted scores per candidate, the command and the ego state), the architecture (two attention blocks, width 128, 0.52 M parameters) and the training target (Appendix W).

[2-4] Questions For Authors

I don't have other questions. Please refer to the Critical Weaknesses section.

Understood, thank you. Our answers are above. If any question remains, we will answer it right away.

Reviewer_FGh4OpenReview ↗
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Paper summary

This paper proposes RethinkDrive, a lightweight trajectory selector for frozen driving planners. The method trains a selector using the candidate closest to a recorded human trajectory and combines its predictions with the planner's existing scores. Experiments on NAVSIM show improvements over the local DiffusionDriveV2 baseline, mainly in temporal consistency, but no clear improvement on DriveSuprim. The paper also studies how different supervision targets and score fusion affect the learned rankings and final driving performance.

Critical strengths
  • Useful empirical study comparing human-reference and metric-based supervision for trajectory selection, particularly when many candidates share the maximum driving score.
  • The analysis of learned rankings before and after score fusion provides useful insight into how the selection rule affects performance. The breakdown of individual driving metrics also helps explain where the improvements come from.
Critical weaknesses
  • The gap between the local DDv2 baseline and the published results raises concerns about the significance of the reported improvement. In particular, the local baseline has a much lower extended comfort score (34 vs. 91), which accounts for most of RethinkDrive's gains. It is unclear whether similar improvements would hold with a stronger planner or a configuration matching the published results. The results on DriveSuprim also raise questions about the generality of the approach.
  • Most of the improvement on DDv2 comes from extended comfort, with reductions in other metrics such as ego progress and drivable-area compliance. This raises the question of whether the method improves driving decisions more broadly or mainly favors temporally consistent trajectories.
Questions for authors
  1. Is there a clear reason why demonstration-nearest supervision produces such a large improvement in temporal consistency? Could the authors investigate whether this comes from changes in speed or progress, or compare against a scorer (rule-based or otherwise) that explicitly accounts for extended comfort?
  2. Can the authors explain the large difference between their local DDv2 baseline and the published results, particularly for extended comfort?
  3. Minor presentation suggestion: Tables 2–4 could highlight the best numerical values in each metric column, perhaps using italics since bold is already used to indicate the proposed method.
1 comment
AuthorsOpenReview ↗

Gain holds on the released checkpoint, mainly through temporal consistency, and shrinks predictably as native EC rises

Thank you very much for the care you gave to our paper. We are sorry for replying so late. The additional experiments, including closed-loop runs, took several days, and we wanted to answer every point carefully, with our analysis.

In the revised PDF your changes are blue, and margin tag 1-n points to answer [1-n].

[1-1] Weakness 1

It is unclear whether similar improvements would hold with a stronger planner or a configuration matching the published results.

This is a fair concern, and we would like to explain where the gain comes from. Our row is the public release of the planner, and we could not reproduce the published row. As you note, extended comfort (EC) accounts for the gain: +4.36 [4.14, 4.56] of the +3.93 (Table 21). EC is the only official term that compares successive plans, and the per-frame training score has none, so the human target helps most where the planner's own consistency is weak.

On the released checkpoint the gain shrinks as native EC rises (+3.93 [3.39, 4.46] at EC 34.0, +3.21 at 41.7, +2.37 at 55.5, Table 33), and +0.29 [−0.18, +0.81] on DriveSuprim (77.3). A rule fixed on these rows predicted +0.29 for a third planner, GTRS-Aug, and we observed −0.37 [−0.78, +0.07], within its tolerance. At the published EC of 91.0 the rule gives −0.76, and we claim no gain there. So the gain is resolved on one of three planners, but we can predict where it appears.

Where to check. Section 5.6 (p. 9, lines 479–485), limitations (p. 10, line 518), Appendices P and X.

[1-2] Weakness 2

This raises the question of whether the method improves driving decisions more broadly or mainly favors temporally consistent trajectories.

We share this question. The method mainly favors temporally consistent trajectories, and we think this is what the human target adds. The per-frame score cannot see whether successive plans agree, whereas a recorded drive is one continuous trajectory, and the official score rewards consistency. With EC excluded, the difference is −0.49 [−1.01, +0.03] (Table 21). Progress falls from 91.2 to 87.8 and drivable-area compliance from 97.8 to 96.7. The progress cost is already in the human target (87.68 against 87.77), and 41% of the drivable-area drop comes from the 5.0% of scenes where the recorded drive itself does not comply (Appendix Y). In closed loop, a related selector that edits one plan without seeing the scene lowered the Bench2Drive score, whereas our own selector showed no detectable loss on two planners in HUGSIM and made DDv2's plans far more comfortable (27.9 to 57.9), as on NAVSIM (Appendix V).

Where to check. Section 5.5 (p. 8, lines 424–425) and limitations (p. 10, lines 518–524).

[1-3] Question 1

Is there a clear reason why demonstration-nearest supervision produces such a large improvement in temporal consistency?

Thank you for the two checks you suggested. We ran both, and we can explain the effect in part.

The reason. The cached score has no term that compares successive plans (answer [1-2]). Executed directly, the candidate nearest to the human trajectory passes the EC test on 62.4% of scenes and the per-frame metric maximum on 18.9% (Appendix U) (p. 4, lines 208–210). The trained selector reaches 79.1%, more than its target, so the cause is identified only in part. Even a metric target with the benchmark's between-frame term trains selectors about 6 points below ours, although its labels pass the EC test more often (98.3% against 79.3%), so this term alone does not produce the gain (Appendix AA).

Speed or progress. Scenes where the selected plan is slower contribute +2.58 of the +3.93, and scenes with unchanged speed +1.44, so the gain is not slower driving alone (Appendix Q) (p. 8, lines 425–427).

A comfort-aware scorer. An EC-aware rule, fixed before the run, ends −0.17 [−0.50, +0.18] from the native planner, and the selector is 4.10 above it (Appendix R) (p. 8, lines 386–387).

[1-4] Question 2

Can the authors explain the large difference between their local DDv2 baseline and the published results, particularly for extended comfort?

We understand why this matters, and we could explain it only in part. Our planner is the released checkpoint, byte for byte (Appendix P). The maintainers state publicly that the NAVSIM v1 and v2 weights differ and that the published row uses the scorer before a bug fix. We could not obtain those weights, so this gap lies outside what we could test. On the released file, sampling moves EC from 34.0 to 55.5, never near 91.0, and the gain holds in all three settings (answer [1-1]).

Where to check. Section 5.6 (p. 9, lines 479–485).

[1-5] Question 3

Tables 2–4 could highlight the best numerical values in each metric column

Done, thank you. Tables 2–4 now print the best value of each column in italics, as the captions say (p. 7, lines 327 and 346) (p. 10, line 492).

If any question remains, we will answer it right away.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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